The Effect of Dipeptidyl Peptidase 4 Inhibition on Growth Hormone Secretion in Women With Polycystic Ovarian Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effect of Dipeptidyl Peptidase 4 Inhibition on Growth Hormone Secretion in Women With Polycystic Ovarian Syndrome (NCT02122380), a randomized phase 4 study. The primary outcome is Mean Overnight Growth Hormone Levels.

2. Clinical Question

The trial’s rationale connected growth hormone secretion with abdominal obesity and cardiometabolic risk, and proposed that sitagliptin might affect growth hormone secretion. The primary endpoint addresses that secretion question directly. The registry also lists outcomes related to insulin secretion, glucose, visceral adipose tissue, and vascular function. Those outcomes provide additional physiological measures, but they do not replace the primary comparison.

The design places each participant in both treatment conditions, so the research question is about a within-participant treatment contrast. That feature is important when interpreting the numerical summaries and the registry-reported test: how the analysis handled the crossover structure is not described in enough detail to establish that the reported test used the paired treatment observations.

3. Trial Design

The registry describes this as a randomized, triple-masked, phase 4 crossover trial. The total enrollment was 23. Participants were assigned to one of two treatment sequences: sitagliptin followed by placebo, or placebo followed by sitagliptin. Sitagliptin was given as 100 mg by mouth daily for 30 days; placebo was given daily for 30 days. The registry record does not report the method used to generate the random sequence, the identities of the parties masked, or whether there was a washout interval between treatment periods.

The primary outcome was collected at the end of each 30-day treatment period during an inpatient visit. Growth hormone was measured every 10 minutes from 8 PM until 8 AM. The registry says the participant-level mean was calculated first, and those participant means were then averaged across participants. The primary analysis population was participants who received both interventions and completed both inpatient visits; each treatment summary includes 16 participants.

The registry describes a crossover, but does not explain the statistical handling of the repeated measurements from the same participants, potential period effects, or the assigned treatment sequence. Those details matter because the two treatment observations from one participant are related rather than independent. The registry reports a Wilcoxon (Mann-Whitney) superiority analysis, but does not state how that method was adapted, if at all, to the crossover design.

The trial is marked completed. The registry lists five outcome measures and four posted secondary outcomes, including early insulin secretion, glucose area under the curve, visceral adipose tissue, and vascular function. The posted numerical secondary results cover three of those outcomes; numerical results for vascular function are not reported in the registry record. The registry does not report the original sample-size justification or the planned analysis details beyond the information attached to the posted analyses.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 23 out of 55 participants were randomized. Of those not randomized, 23 were did not meet inclusion criteria and 9 declined to participate.

First Intervention (30 Days)

Reasons for not completing this period:

Washout (8 Weeks)

Reasons for not completing this period:

Second Intervention (30 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants who received both interventions and completed both inpatient visits were included in the analysis. (1 participant was unable to complete their 2nd inpatient visit due to a family emergency. A 2nd participant was unable to complete the overnight portion of the inpatient visit due to illness in a family member.)

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All participants randomized to an intervention are included.

6. Primary Endpoint

The registry lists the primary outcome as Mean Overnight Growth Hormone Levels, measured over At completion of 30 days of placebo treatment and at completion of 30 days of sitagliptin treatment; every 10 minutes from 8 PM until 8 AM..

The primary endpoint is mean overnight growth hormone concentration, measured in ng/mL. During the final inpatient visit of each treatment period, growth hormone levels were measured every 10 minutes from 8 PM until 8 AM. The values for each participant were averaged to produce a participant-level mean, and those means were then averaged across participants for each treatment.

This endpoint was chosen to assess the trial’s central physiological question: whether treatment with sitagliptin was associated with a difference in overnight growth hormone levels compared with placebo. Repeated overnight sampling captures variation over the measurement period more fully than a single blood measurement would. Averaging the repeated measurements also yields a continuous participant-level outcome that can be compared across treatment conditions.

The registry reports a placebo mean of 0.85 ng/mL with a standard deviation of 0.54, and a sitagliptin mean of 0.84 ng/mL with a standard deviation of 0.51. The unadjusted mean difference, sitagliptin minus placebo, is -0.01 ng/mL. These summaries describe the observed measurements; they do not by themselves establish the precision or design appropriateness of the treatment comparison. In particular, the crossover means that the within-participant differences are relevant, but the registry does not report their variability or clearly explain how the reported test accounted for that pairing.

Growth hormone secretion was the primary physiological measure, not a direct measure of cardiovascular events, diabetes, or long-term clinical outcomes. The registry’s rationale discusses those broader concerns, but the primary endpoint addresses overnight hormone levels during the treatment periods.

7. Results Posted in the Registry

• Sitagliptin: mean 0.84 versus 0.85 on control; difference -0.01 (95% CI -0.37 to 0.35), standardized effect d = -0.02; z-test p = 0.957.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Early Insulin Secretion During Oral Glucose Tolerance Test

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Sitagliptin: mean 1,871 versus 1,522 on control; difference 349.20 (95% CI -185.45 to 883.85), standardized effect d = 0.43; z-test p = 0.200.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

Area Under the Curve (AUC) for Blood Glucoses During 75 Gram Oral Glucose Tolerance Test

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Sitagliptin: mean 13,878 versus 15,354 on control; difference -1,476 (95% CI -3,175 to 222.22), standardized effect d = -0.57; z-test p = 0.088.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

Visceral Adipose Tissue

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Sitagliptin: mean 1,055 versus 1,142 on control; difference -86.80 (95% CI -561.02 to 387.42), standardized effect d = -0.12; z-test p = 0.720.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover additional physiological outcomes related to insulin secretion, glucose response, and visceral adipose tissue. Across these outcomes, the estimated directions and the registry-reported rank-test results are not uniform. Some rank-test p-values are smaller than the conventional 0.05 reference point, while others are not. This mixed pattern does not form a consistent set of secondary findings that independently clarifies the primary result.

These measures relate to the primary question by describing other metabolic or body-composition outcomes during the treatment periods. They are not alternative measures of overnight growth hormone secretion, and they do not resolve the uncertainty around the primary treatment contrast. Vascular function is listed as a secondary outcome, but numerical results for it are not reported in the registry record.

Secondary outcomes generally carry less inferential weight than the primary outcome because they are additional comparisons and the registry does not report a multiplicity adjustment. When several hypotheses are tested, the chance of at least one apparently notable result arising by chance can increase. This is a general statistical concern, not proof that any particular secondary result is spurious. The record does not report a prespecified hierarchy, correction procedure, or detailed analysis plan for these outcomes.

The reported secondary tests also share the registry’s Wilcoxon (Mann-Whitney) label. As with the primary outcome, the record does not explain whether or how the analyses account for the crossover pairing. The separate mean-difference recalculations are based on aggregate summaries and should be read as unadjusted descriptive analyses rather than a complete paired analysis. The overall secondary pattern is therefore useful for context, but it should not be used to make a firm conclusion about treatment effects or to override the primary result.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Early Insulin Secretion During Oral Glucose Tolerance Test
• Area Under the Curve (AUC) for Blood Glucoses During 75 Gram Oral Glucose Tolerance Test
• Visceral Adipose Tissue
• Vascular Function (Endothelium-dependent Vasodilation)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary summary measure?

The primary outcome is continuous, and the registry reports a mean and standard deviation for each treatment. A mean describes the average participant-level overnight growth hormone value. A standard deviation describes how dispersed participant values are around that average; it is not the uncertainty of the mean itself. The reported summaries are based on 16 participants in each treatment condition, drawn from a crossover population that completed both treatment periods and inpatient visits.

In general, a mean difference is the treatment-group mean minus the comparator mean. Here, the reported unadjusted contrast is sitagliptin minus placebo, with an estimate of -0.01 ng/mL. The negative sign indicates that the posted sitagliptin mean is slightly lower than the placebo mean. The estimate is descriptive; its uncertainty and the assumptions used to calculate it matter when judging how informative it is.

How do the analyses differ?

The registry reports a Wilcoxon (Mann-Whitney) superiority test for the primary comparison, with p = 0.918. This is a rank-based method rather than a test of the difference between means. In general, rank-based tests compare the ordering of observations and can be useful when distributional features make a mean-based model less suitable. Their interpretation is not automatically a test of a difference in means.

The recalculated result is an unadjusted comparison based on the posted means and standard deviations. It gives a mean difference and a confidence interval for that difference, along with p = 0.957. This calculation does not reproduce the sponsor’s rank-based analysis. It also does not incorporate participant-level pairing, because the posted aggregate summaries do not contain the within-person differences needed to do so.

In general, crossover data are paired: each participant contributes an outcome under both treatments. A paired analysis uses the within-participant treatment difference and its variability. That approach can account for the fact that a participant’s two measurements may be related. The registry’s use of a Wilcoxon (Mann-Whitney) label does not itself explain whether paired data were used, and the record does not report a crossover-specific model, period adjustment, sequence adjustment, or a paired rank test. The posted information therefore does not permit a full assessment of the analysis relative to the design.

What does a confidence interval convey?

In general, a confidence interval describes a range of values compatible with the data under the calculation’s assumptions. It communicates both the direction and precision of an estimated contrast. If an interval for a mean difference includes zero, the data are compatible with no mean difference as well as with differences on either side of zero. This does not prove equality. The primary interval crosses zero, and its breadth means that the point estimate alone should not be treated as a precise estimate of the underlying treatment contrast.

A confidence interval is not a range that contains a fixed proportion of individual participant values. Nor is it the probability that the true effect lies within the particular interval. Its interpretation is tied to the method used to calculate it. Here, the interval accompanies an unadjusted summary-statistic recalculation, rather than the registry-reported rank-based analysis.

Why can dispersion and distribution matter?

In general, substantial variability among participants makes it harder to estimate an average difference precisely, especially when the analysis population is small. A standard deviation describes observed spread, while the standard error describes uncertainty in an estimated mean. The registry reports standard deviations and separately posted standard errors for the treatment means. Neither the mean nor standard deviation alone conveys the full paired variability needed for a crossover comparison.

General statistical methods also distinguish ordinary spread from over-dispersion: over-dispersion occurs when variability is greater than a model expects, and can make model-based uncertainty estimates too small if not addressed. The registry does not report an over-dispersion assessment or a model requiring such an assessment. It would therefore be inappropriate to assert that over-dispersion affected these results.

How should the p-values be read?

In general, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions were correct. It is not an effect size, a measure of clinical importance, or a probability that the null hypothesis is true. A high p-value does not establish that two treatments are equivalent. Equivalence or non-inferiority questions require a prespecified margin and a design and analysis suited to that question; such a margin is not reported in the registry record.

The registry labels the analyses as superiority tests. No adjustment for multiple outcome testing is reported. The primary outcome remains the main stated question, while secondary analyses are additional comparisons. A collection of unadjusted p-values can produce apparently notable results by chance, so secondary findings require more caution than a single prespecified primary comparison.

What can the posted summaries not establish?

Aggregate summaries cannot show the distribution of individual outcomes, the sequence-specific results, or whether treatment effects differed by period. They also cannot establish whether missing observations were related to the outcomes. The trial’s original statistical analysis plan, sample-size justification, detailed handling of the crossover, and interim analyses are not reported in the registry record. These omissions limit the ability to judge whether the posted analyses match the intended design and plan.

11. Confidence Intervals and Precision

The primary mean difference is -0.01 ng/mL, with a confidence interval that extends from below zero to above zero. Because zero lies within the interval, the summary-statistic analysis does not tightly distinguish a negative mean difference from a positive one. The interval is wide in relation to the estimated difference, so the point estimate should not be read as precise evidence that the underlying difference is exactly -0.01 ng/mL.

Precision is affected by the amount of observed variation and the number of analyzed participants. The primary treatment summaries each include 16 participants, with standard deviations of 0.54 ng/mL for placebo and 0.51 ng/mL for sitagliptin. In general, greater variation or fewer observations tends to widen uncertainty, although a crossover comparison also depends on the correlation between each participant’s two treatment measurements. That within-participant information is not reported.

The registry’s rank-based analysis reports p = 0.918, while the unadjusted recalculation from the means and standard deviations gives p = 0.957. These p-values are not interchangeable estimates of the confidence interval. The registry does not provide a confidence interval for its rank-based test, nor enough information to recreate a paired interval for the crossover contrast.

Secondary intervals also vary in width and include values on both sides of zero for the posted unadjusted mean differences. They reflect uncertainty in those particular recalculations and should not be treated as adjusted evidence across multiple outcomes. Overall, the primary estimate has limited precision, and the registry does not supply the paired data or analysis detail that would allow a more complete evaluation of the crossover contrast.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning estimates are participants per arm, not total events. They are illustrations calculated from the observed effect, not the trial’s own design justification. The assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s sample-size assumptions are not reported in the registry record.

The 80% power column describes a planned study’s chance of detecting the specified effect under the stated assumptions if that effect is the true one. The 90% power column describes a higher target chance under those same assumptions. These are design targets, not guarantees about any future study, and neither column tells how likely the observed result is to be true. The estimates are not observed power.

Each planning row considers a different fraction of the observed effect. When the target effect is smaller, more participants are needed to distinguish it from random variation at the same significance and power targets. For the primary outcome, the observed mean difference is -0.01 ng/mL, and the planning illustration consequently gives very large participant requirements. Such estimates are particularly sensitive to a very small observed effect and should not be mistaken for a recommendation or for the trial’s original enrollment target.

The planning calculations use equal allocation between two arms, whereas the actual trial is described as a randomized crossover. The calculation is therefore a generic illustration and does not model the within-participant structure of this trial. A design-specific planning analysis would require assumptions about the paired treatment differences and other design features; those assumptions are not reported in the registry record. The planning estimates should be read as conditional arithmetic under the listed assumptions, not as a reconstruction of the trial’s original planning process.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.010; pooled standard deviation σ = 0.525.
2. n = 2 × (1.96 + 0.842)² × 0.525² / -0.010² = 43,302.3, rounded up to 43,303 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.01                      # observed difference in means
sigma <- 0.525214242000348                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2122380)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 43,303 (80% power), 57,970 (90% power)
 75% of observed effect: n per arm = 76,982 (80% power), 103,057 (90% power)
 50% of observed effect: n per arm = 173,210 (80% power), 231,878 (90% power)
power.t.test: 43303.2 
Simulated power at n = 43,303 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary superiority analysis as a Wilcoxon (Mann-Whitney) test with p = 0.918. The separate unadjusted recalculation from the posted treatment means and standard deviations gives a mean difference of -0.01 ng/mL, a confidence interval spanning zero, and p = 0.957. The registry marks the comparison as having no discrepancy.

These results are not identical because they use different information and methods. The sponsor-reported test is rank-based. The recalculation estimates a mean difference from aggregate summaries and cannot use the individual paired differences from the crossover. The recalculation is therefore a supplementary description, not a replacement for the registry-reported analysis.

The registry does not provide participant-level data, details of a crossover-specific analysis, or a confidence interval for the reported rank test. It is consequently not possible to determine from the record how the sponsor handled pairing, period, or sequence. The two p-values should be understood as outputs of distinct analyses, not as competing versions of one calculation. The posted record’s own analysis remains the reported analysis, while the recalculation helps describe the mean contrast and its uncertainty under its stated, unadjusted approach.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and several secondary outcomes, but does not report a multiplicity-control procedure. In general, testing multiple outcomes increases the opportunity for at least one result to appear noteworthy by chance. A prespecified hierarchy, family-wise error adjustment, or other planned strategy can help define how multiple tests should be interpreted. None of those details is reported in the registry record, so the posted secondary p-values should be treated as unadjusted unless the registry states otherwise.

The record reports that the primary analysis included participants who received both interventions and completed both inpatient visits. Each primary treatment summary has 16 participants. It also notes that one participant could not complete the second inpatient visit because of a family emergency and that another could not complete the overnight portion of an inpatient visit; the remaining reason text is incomplete in the registry record. The record does not explain how the other enrolled participants were handled or provide a full accounting of missing observations across outcomes.

For the secondary outcomes, the posted summaries use 18 participants for early insulin secretion and glucose area under the curve, and 17 for visceral adipose tissue. Reasons for these differing analysis counts, and the treatment of missing measurements, are not reported in the registry record. The record does not say whether missing outcomes were imputed, whether a complete-case approach was used for every outcome, or whether sensitivity analyses assessed the effect of missingness. It is not possible to infer the missing-data mechanism from the counts alone.

The crossover design makes the analysis population and missing-data handling particularly relevant: a participant may have data from one period but not the other, and the registry’s primary population requires completion of both interventions and inpatient visits. The record does not report how partial crossover data were used. It also does not report the original statistical analysis plan, interim analyses, or detailed approaches to period and sequence effects. These absences limit assessment of both multiplicity and the robustness of the posted analyses.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pancreatitis (5.0%).

The registry reports serious adverse events for 20 participants at risk during sitagliptin and 21 during placebo. One participant in the sitagliptin group was recorded as having a serious adverse event; none was recorded in the placebo group. No deaths were reported in either group. The registry lists pancreatitis as a top serious adverse event term with 5.0%.

Other adverse events were reported for 5 of 20 participants at risk during sitagliptin and 9 of 21 during placebo. These are counts of participants reported as affected, not measures of severity or proof that treatment caused an event. The registry does not provide enough detail in these figures to establish the timing, relatedness, or clinical course of individual events. The serious-event counts should be read descriptively, especially given the small number of participants and the different at-risk counts. They do not establish comparative safety or exclude uncommon harms.

17. What the Result Does, and Does Not, Mean

The primary posted means were similar: 0.85 ng/mL during placebo and 0.84 ng/mL during sitagliptin. The unadjusted mean difference was -0.01 ng/mL, and the registry-reported rank-based analysis gave p = 0.918. The summary-statistic confidence interval spans zero, indicating uncertainty about both the direction and size of the mean contrast. These results describe the measurements in the analyzed participants; they do not prove that the treatments have identical effects.

The study addresses overnight growth hormone levels after 30-day treatment periods in women with polycystic ovary syndrome. It does not directly establish effects on cardiovascular events, diabetes, long-term glucose control, or other clinical outcomes. Although the registry rationale links growth hormone secretion to broader metabolic and vascular concerns, those concerns are not the primary endpoint measured.

The crossover format could support a within-participant comparison, but the registry does not report enough analysis detail or paired variability to determine how fully that feature was used. The primary analysis includes 16 participants who completed both treatment conditions and inpatient visits, fewer than the total enrollment of 23. Incomplete observations and the lack of a complete missing-data account further limit what can be concluded.

Secondary outcomes offer additional context but do not resolve the primary uncertainty. Their analyses are unadjusted in the registry record, and no multiplicity procedure is reported. The result should therefore be understood as a small, completed trial with an imprecise primary mean contrast and incomplete reporting of important analytic details—not as a definitive statement that sitagliptin does or does not affect growth hormone secretion.

No medical recommendation follows from these statistics. They are a description of this trial’s posted outcomes and their uncertainty, within the limits of its analyzed population and the information available in the registry record.

18. Why This Trial Matters Statistically

This trial is statistically interesting because its crossover design allows each participant to receive both sitagliptin and placebo. In general, a well-analyzed crossover can use within-person comparisons to account for stable differences between participants. That potential advantage depends on measuring and analyzing the paired treatment contrast appropriately. The registry gives treatment means and standard deviations but does not report the paired differences or clearly explain how the stated Wilcoxon (Mann-Whitney) method was applied to the crossover structure.

The example also shows why a point estimate and its precision should be considered together. The primary means are close and the recalculated mean difference is small, but the interval crosses zero and is broad relative to that estimate. A nonsignificant p-value is not evidence of equivalence; it indicates that the analysis did not identify a clear difference under its test and assumptions. A prespecified equivalence margin is not reported.

The posted secondary outcomes illustrate another important issue: multiple outcomes can produce a varied pattern of results. Without a reported multiplicity strategy, isolated secondary p-values deserve cautious interpretation. The distinction between a primary question and additional outcomes helps prevent exploratory findings from being treated as confirmatory evidence.

Finally, the record highlights the limits of planning illustrations based on an observed effect. A near-zero observed primary contrast yields very large illustrative sample-size estimates, but those calculations are not the trial’s own design justification and do not recreate a crossover-specific power analysis. The original planning assumptions are not reported. Taken together, the design, analysis reporting, precision, and multiplicity issues provide a practical example of why statistical interpretation depends on more than a single p-value.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the available record. The primary analysis is restricted to 16 participants who received both interventions and completed both inpatient visits, while total enrollment was 23. The registry describes two incomplete visits, but the second reason is truncated, and it does not provide a complete accounting of the remaining difference between enrollment and outcome-specific analysis counts. The effect of missing observations cannot be assessed from the posted summaries.

The registry identifies a randomized crossover design but does not report a detailed paired analysis, treatment-period or sequence effects, or a washout interval. The named Wilcoxon (Mann-Whitney) method does not by itself clarify how the repeated measurements from the same participants were handled. Aggregate means and standard deviations cannot recover the within-participant variability needed to evaluate a paired mean contrast.

The record does not report the original sample-size justification, a detailed statistical analysis plan, interim analyses, or a multiplicity strategy. The planning illustrations are based on the observed effect under stated generic assumptions, not on the trial’s original design. The registry also does not provide a numerical result for the listed vascular-function outcome. These reporting gaps constrain assessment of the intended analysis and the breadth of the outcome evidence.

The trial’s enrollment and outcome-specific analysis groups are small, and the primary confidence interval is broad. The posted results therefore offer limited precision. The listed adverse-event counts are descriptive and do not establish causality or comparative safety. These limitations should frame interpretation without implying that unreported procedures were or were not performed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The Effect of Dipeptidyl Peptidase 4 Inhibition on Growth Hormone Secretion in Women With Polycystic Ovarian Syndrome — NCT02122380.
• Registry record last updated 2020-05-08; status last verified 2020-04.
• Results first posted 2020-05-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, randomized, triple-masked, phase 4 crossover trial with enrollment of 23. Participants received sitagliptin 100 mg daily and placebo in 30-day treatment periods. The primary outcome was mean overnight growth hormone concentration, measured every 10 minutes from 8 PM until 8 AM at the end of each period.

Among 16 participants in the primary analysis, the reported means were 0.85 ng/mL for placebo and 0.84 ng/mL for sitagliptin. The registry’s Wilcoxon (Mann-Whitney) test reported p = 0.918. A separate unadjusted mean-difference calculation was -0.01 ng/mL, with an interval spanning zero. The registry also posted results for three secondary outcomes and descriptive adverse-event counts.

Interpretation is limited by imprecision, incomplete detail on crossover analysis and missing data, and the absence of a reported multiplicity strategy or original sample-size justification. The registry record does not establish effects on broader clinical outcomes.